Common Mistakes in Statistics & Probability

328 common pitfalls across 82 concepts, including 82 recurring stuck points

These are the pitfalls students hit across all 82 statistics & probability concepts, from Mean, Median and Mode onward. Each entry names the concept it comes from, so you can tell a slip from a genuine gap and go straight to the explanation.

1
Mean
Stuck Point

The procedure for mean is the easy part; the trap is forgetting to divide by the count after adding. Asking "Am I adding up all the values and dividing by how many there are?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

2
Mean
Mistake

Forgetting to divide by the count after adding — the mean is the sum per value, not the sum itself.

3
Mean
Mistake

Counting the number of values wrong (off by one) — divide by exactly how many data points you added.

4
Mean
Mistake

Using the mean on outlier-heavy data — when one value is far from the rest, switch to the median for a typical value.

5
Median
Stuck Point

The procedure for median is the easy part; the trap is finding the middle of the unsorted list. Asking "After sorting the data smallest to largest, what value sits exactly in the middle?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

6
Median
Mistake

Finding the middle of the unsorted list — always sort smallest to largest before locating the middle.

7
Median
Mistake

Picking one middle value when n is even — average the two middle values instead.

8
Median
Mistake

Using the position number n+12 as the answer — that is the position of the median, not its value.

9
Mode
Stuck Point

The procedure for mode is the easy part; the trap is reporting the frequency instead of the value. Asking "Which value occurs more often than any other?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

10
Mode
Mistake

Reporting the frequency instead of the value — the mode is the data value that repeats most, not how many times it repeats.

11
Mode
Mistake

Saying 'no mode' when several values tie — if two or more values tie for most frequent, the data is bimodal/multimodal and all are modes.

12
Mode
Mistake

Forcing a mode on data where every value is unique — if nothing repeats, there is no mode.

13
Range (Statistics)
Stuck Point

The procedure for range (statistics) is the easy part; the trap is subtracting in the wrong order and getting a negative. Asking "Am I just subtracting the smallest value from the largest?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

14

Subtracting in the wrong order and getting a negative — always do max⁡−min⁡ so the range is non-negative.

15

Forgetting to find the true max and min in an unsorted list — scan the whole list, do not assume the first and last entries are the extremes.

16

Trusting the range when an outlier is present — one extreme value inflates it, so switch to IQR for a robust spread.

17
Standard Deviation
Stuck Point

The procedure for standard deviation is the easy part; the trap is forgetting the square root. Asking "Am I measuring how far values typically fall from the mean, in the data's own units?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

18

Forgetting the square root — that gives variance, not standard deviation.

19

Dropping the squaring of deviations — positive and negative distances would cancel; square them first.

20

Dividing a sample by n when you should divide by n−1 — sample SD (s) uses n−1, population SD (σ) uses n.

21
Variance
Stuck Point

The procedure for variance is the easy part; the trap is taking the square root and calling it variance. Asking "Am I averaging the squared distances from the mean (and not taking the square root)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

22
Variance
Mistake

Taking the square root and calling it variance — that result is the standard deviation; variance is before the root.

23
Variance
Mistake

Averaging the deviations without squaring — raw deviations sum to zero, so square them first.

24
Variance
Mistake

Mixing up the divisor — population variance divides by n, sample variance (s2) divides by n−1.

25
Probability
Stuck Point

The procedure for probability is the easy part; the trap is counting outcomes that are not equally likely. Asking "Are the outcomes equally likely, and am I asked how likely (not how many)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

26
Probability
Mistake

Counting outcomes that are not equally likely — the favorable-over-total rule needs equally-likely outcomes.

27
Probability
Mistake

The gambler’s fallacy: thinking past results change the next independent event — a fair coin has no memory.

28
Probability
Mistake

Reporting a count instead of a probability — the answer must be between 0 and 1 (or a percent), not a raw number of ways.

29
Sample Space
Stuck Point

The procedure for sample space is the easy part; the trap is merging distinct outcomes. Asking "Have I listed every distinct outcome that could occur, with none missing or merged?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

30
Sample Space
Mistake

Merging distinct outcomes — HT and TH are different; treating them as one shrinks the sample space.

31
Sample Space
Mistake

Forgetting an outcome — every probability divides by ∣S∣, so a missing outcome corrupts the answer.

32
Sample Space
Mistake

Listing outcomes that are not equally likely without saying so — the favorable-over-total shortcut assumes equal likelihood.

33
Independent Events
Stuck Point

The procedure for independent events is the easy part; the trap is multiplying probabilities for without-replacement draws. Asking "Does the first event happening change the probability of the second?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

34

Multiplying probabilities for without-replacement draws — those are dependent; use the updated second probability.

35

Confusing independent with mutually exclusive — independent events can both happen (product nonzero); mutually exclusive cannot (P(A and B)=0).

36

Adding instead of multiplying for 'and' — use + for 'or' on exclusive events, × for 'and' on independent ones.

37

The procedure for conditional probability is the easy part; the trap is dividing by the whole sample space. Asking "Has some information already been revealed that shrinks the set of possible outcomes?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

38

Dividing by the whole sample space — divide by P(B), the known condition, which shrinks the denominator.

39

Swapping P(A∣B) and P(B∣A) — read carefully which event is the 'given.'

40

Assuming independence to skip the formula — only set P(A∣B)=P(A) if you have verified the events are independent.

41
Expected Value
Stuck Point

The procedure for expected value is the easy part; the trap is averaging the outcome values without weighting by probability. Asking "Am I weighting each outcome by its probability and summing to get a long-run average?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

42

Averaging the outcome values without weighting by probability — multiply each value by its chance first.

43

Letting the probabilities not sum to 1 — a complete set of outcomes must have probabilities adding to 1.

44

Treating E(X) as the result of one trial — it is the long-run average, which need not be an achievable single outcome.

45

The procedure for normal distribution is the easy part; the trap is applying the 68-95-99.7 rule to non-normal data. Asking "Is the data single-peaked, symmetric, and described by just a mean and a standard deviation?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

46

Applying the 68-95-99.7 rule to non-normal data — the rule only holds for the symmetric bell.

47

Assuming any single-peaked data is normal — check for symmetry; a long tail means skew, not normal.

48

Confusing the curve's height with probability — for a continuous curve, probability is area under it over an interval, not the height at a point.

49
Z-Score
Stuck Point

The procedure for z-score is the easy part; the trap is forgetting to divide by σ. Asking "Am I expressing this value as a number of standard deviations from its mean?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

50
Z-Score
Mistake

Forgetting to divide by σ — x−μ alone is a raw deviation, not a z-score.

51
Z-Score
Mistake

Dropping the sign — a negative z means below the mean; the sign carries direction.

52
Z-Score
Mistake

Using the wrong distribution's mean and SD — standardize each value with its own data set's μ and σ.

53
Permutation
Stuck Point

The procedure for permutation is the easy part; the trap is using a permutation when order doesn't matter. Asking "Does swapping two of the chosen items create a different valid outcome?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

54
Permutation
Mistake

Using a permutation when order doesn't matter — that overcounts by r!; use a combination instead.

55
Permutation
Mistake

Allowing repeats — P(n,r) assumes distinct items each used once; repeats need the counting principle.

56
Permutation
Mistake

Confusing n and r in n!(n−r)! — n is the pool, r is how many positions you fill.

57
Combination
Stuck Point

The procedure for combination is the easy part; the trap is forgetting to divide by r!. Asking "Does rearranging the chosen items leave it the same selection?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

58
Combination
Mistake

Forgetting to divide by r! — that leaves a permutation count, which overcounts the orderings.

59
Combination
Mistake

Using a combination when order matters — assignments and rankings need a permutation.

60
Combination
Mistake

Mixing up r and n−r — note C(n,r)=C(n,n−r), so choosing 3 to keep equals choosing the others to drop.

61
Factorial
Stuck Point

The procedure for factorial is the easy part; the trap is setting 0!=0. Asking "Am I counting the ways to arrange all n distinct items, multiplying n down to 1?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

62
Factorial
Mistake

Setting 0!=0 — by definition 0!=1, which keeps the permutation/combination formulas consistent.

63
Factorial
Mistake

Multiplying only down to a wrong stopping point — go all the way to 1 (e.g. 4!=4⋅3⋅2⋅1, not 4⋅3⋅2).

64
Factorial
Mistake

Confusing n! with n2 or 2n — factorial multiplies a descending run, not a square or a double.

65
Correlation
Stuck Point

The procedure for correlation is the easy part; the trap is saying correlation proves causation. Asking "Do the dots show a direction and tightness of pattern?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

66
Correlation
Mistake

Saying correlation proves causation — association alone is not proof of cause.

67
Correlation
Mistake

Calling any upward pattern strong — strength depends on how tightly dots cluster around the trend.

68
Correlation
Mistake

Using correlation with categorical data — correlation needs paired numerical variables.

69
Scatter Plot
Stuck Point

The procedure for scatter plot is the easy part; the trap is connecting scatter-plot dots automatically. Asking "Does each dot need both an x-value and a y-value?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

70
Scatter Plot
Mistake

Connecting scatter-plot dots automatically — dots show cases, not necessarily a path.

71
Scatter Plot
Mistake

Using categories as if they were paired measurements — scatter plots need numerical x and y values.

72
Scatter Plot
Mistake

Claiming causation from a visible trend — association alone does not prove cause.

73
Histogram
Stuck Point

The procedure for histogram is the easy part; the trap is leaving gaps between bars. Asking "Am I grouping one numeric variable into intervals and showing the count in each?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

74
Histogram
Mistake

Leaving gaps between bars — histogram bins are continuous, so bars should touch (gaps mean a categorical bar graph).

75
Histogram
Mistake

Using unequal bin widths carelessly — equal-width bins keep bar heights comparable as counts.

76
Histogram
Mistake

Treating the tallest bar as the mean — it shows the most common bin (the mode region), not the average.

77
Box Plot
Stuck Point

The procedure for box plot is the easy part; the trap is reading box width as a count of data. Asking "Am I summarizing or comparing distributions using min, Q1, median, Q3, and max?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

78
Box Plot
Mistake

Reading box width as a count of data — each section holds 25% of values; width shows spread, not frequency.

79
Box Plot
Mistake

Forgetting outliers extend the whiskers only to non-outlier values — points beyond the 1.5×IQR fences are plotted separately.

80
Box Plot
Mistake

Confusing the median line with the mean — the box plot shows the median, which the mean need not match in skewed data.

81
Quartiles
Stuck Point

The procedure for quartiles is the easy part; the trap is splitting by equal value width instead of equal count. Asking "Am I splitting ordered data into four groups that each contain the same fraction of the values?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

82
Quartiles
Mistake

Splitting by equal value width instead of equal count — quartiles divide the data into equal numbers of points, not equal ranges.

83
Quartiles
Mistake

Forgetting to order the data first — quartiles, like the median, require a sorted list.

84
Quartiles
Mistake

Confusing Q2 with the mean — Q2 is the median (the 50th-percentile rank), which may differ from the average.

85

The procedure for interquartile range is the easy part; the trap is subtracting min from max instead of Q3−Q1. Asking "Am I measuring the width of the middle half of sorted data, not the full extent?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

86

Subtracting min from max instead of Q3−Q1 — the IQR uses the quartiles, never the extreme values.

87

Computing quartiles on unsorted data — order the data from smallest to largest before finding Q1 and Q3.

88

Confusing Q3−Q1 with Q2 — the IQR is a width (a difference), not the median itself.

89
Data (Abstract)
Stuck Point

The procedure for data (abstract) is the easy part; the trap is treating a summary like the mean as the data. Asking "Is this the raw set of recorded observations, before any summary or conclusion?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

90

Treating a summary like the mean as the data — data is the raw recorded values, not numbers computed from them.

91

Ignoring whether values are numbers or categories — you cannot average colors, so label the data type first.

92

Forgetting to record the question the data answers — context decides which graph and summary make sense.

93
Measurement
Stuck Point

The procedure for measurement is the easy part; the trap is writing a number without a unit. Asking "Have I named the one attribute and the unit before writing the number?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

94
Measurement
Mistake

Writing a number without a unit — every measurement is a number paired with the unit of its attribute.

95
Measurement
Mistake

Measuring the wrong attribute — decide whether you need length, mass, time, or count before picking a tool.

96
Measurement
Mistake

Mixing units in one comparison — convert to a common unit before comparing 30 cm to 1 m.

97
Variability
Stuck Point

The procedure for variability is the easy part; the trap is reporting only the mean and stopping. Asking "Am I describing how scattered the values are, separate from where they center?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

98
Variability
Mistake

Reporting only the mean and stopping — a mean with no spread hides whether the data is consistent.

99
Variability
Mistake

Assuming equal means imply equal data — same center can come with very different variability.

100
Variability
Mistake

Confusing high variability with a high average — spread measures distances from the center, not the center's size.

101
Noise
Stuck Point

The procedure for noise is the easy part; the trap is explaining every fluctuation with a cause. Asking "Is this variation random with no consistent direction or cause?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

102
Noise
Mistake

Explaining every fluctuation with a cause — random noise has no cause, so don't invent one.

103
Noise
Mistake

Reacting to one noisy data point as a trend — wait for a consistent direction before calling it a pattern.

104
Noise
Mistake

Confusing noise with outliers — noise is widespread small wiggle; an outlier is one far-off value.

105
Signal vs Noise
Stuck Point

The procedure for signal vs noise is the easy part; the trap is calling any difference a real effect. Asking "Is the difference larger than the data's ordinary random fluctuation?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

106

Calling any difference a real effect — compare it to the size of the random noise first.

107

Dismissing a true effect as noise — a difference much larger than the usual wiggle is likely signal.

108

Forgetting more data sharpens the call — small samples have so much noise that real signals hide.

109

The procedure for distribution (intuition) is the easy part; the trap is summarizing shape with only the mean. Asking "Am I asking about the overall shape of the values, not one summary number?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

110

Summarizing shape with only the mean — a single number can't show skew, peaks, or gaps.

111

Assuming symmetry by default — check for a long tail before trusting the mean.

112

Ignoring the horizontal scale — the same counts on a stretched axis look like a different shape.

113
Center vs Spread
Stuck Point

The procedure for center vs spread is the easy part; the trap is comparing groups by center alone. Asking "Have I reported both where the data sits and how spread out it is?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

114

Comparing groups by center alone — equal means can hide very different spreads.

115

Pairing the wrong partners — use mean with standard deviation, and median with IQR.

116

Reporting spread without center (or vice versa) — a complete summary needs both.

117
Outliers (Deep)
Stuck Point

The procedure for outliers (deep) is the easy part; the trap is eyeballing outliers without the fence. Asking "Does this value fall beyond Q1−1.5×IQR or Q3+1.5×IQR?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

118

Eyeballing outliers without the fence — compute Q1−1.5×IQR and Q3+1.5×IQR to flag them.

119

Deleting outliers automatically — first decide if it's an error, a rare event, or a meaningful exception.

120

Calling the maximum an outlier by default — the largest value isn't unusual unless it passes the fence.

121
Randomness
Stuck Point

The procedure for randomness is the easy part; the trap is expecting random sequences to alternate neatly. Asking "Is each single outcome unpredictable while the long-run rates stay fixed?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

122
Randomness
Mistake

Expecting random sequences to alternate neatly — real randomness produces streaks and clusters.

123
Randomness
Mistake

Believing past outcomes affect the next independent one — randomness has no memory.

124
Randomness
Mistake

Confusing randomness (no pattern) with bias (a consistent tilt) — bias is predictable, randomness is not.

125
Chance
Stuck Point

The procedure for chance is the easy part; the trap is calling a guaranteed event a matter of chance. Asking "Could this go more than one way, with no way to control which?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

126
Chance
Mistake

Calling a guaranteed event a matter of chance — chance needs at least two genuinely possible outcomes.

127
Chance
Mistake

Thinking you can control a chance outcome — wishing for red doesn't change the spinner.

128
Chance
Mistake

Jumping straight to a number — chance is the informal idea; probability is where the number comes in.

129

The procedure for probability as expectation is the easy part; the trap is expecting the exact expected count. Asking "Am I predicting a long-run count or share, not a single outcome?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

130

Expecting the exact expected count — n⋅P is the long-run average, not a promise for any one run.

131

Applying it to a single trial — probability-as-expectation describes many repetitions, not one outcome.

132

Confusing the predicted count with a probability — n⋅P is a count, while P stays between 0 and 1.

133
Events (Formal)
Stuck Point

The procedure for events (formal) is the easy part; the trap is treating an event as one outcome. Asking "Am I naming a set of outcomes that make a yes/no question true?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

134

Treating an event as one outcome — an event like 'even' is the whole set {2,4,6}.

135

Forgetting the complement shortcut — P(at least one)=1−P(none) uses P(Ac)=1−P(A).

136

Mixing up AND with OR — A∩B needs both true; A∪B needs at least one.

137

The procedure for dependence (statistical) is the easy part; the trap is multiplying P(A)×P(B) for dependent events. Asking "Does knowing the first event occurred change the probability of the second?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

138

Multiplying P(A)×P(B) for dependent events — use P(A)×P(B∣A) instead.

139

Forgetting the pool changed — after a draw without replacement, update the counts before the next probability.

140

Equating dependence with causation — linked probabilities don't prove one causes the other.

141
Causation
Stuck Point

The procedure for causation is the easy part; the trap is reading correlation as causation. Asking "Would deliberately changing X reliably change Y, not just co-occur with it?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

142
Causation
Mistake

Reading correlation as causation — co-movement alone never proves cause; check for confounders.

143
Causation
Mistake

Ignoring lurking variables — a hidden third factor can manufacture a spurious link.

144
Causation
Mistake

Forgetting direction — a link between X and Y might mean Y causes X (more police are sent where there is more crime), not that X causes Y.

145
Sampling Bias
Stuck Point

The procedure for sampling bias is the easy part; the trap is believing a large sample cures bias. Asking "Did the selection method systematically include or exclude certain groups?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

146

Believing a large sample cures bias — only fixing the selection method removes a systematic tilt.

147

Using convenience samples and generalizing — easy-to-reach groups rarely mirror the population.

148

Confusing bias with random error — bias is a consistent directional skew, not symmetric chance variation.

149
Representativeness
Stuck Point

The procedure for representativeness is the easy part; the trap is assuming a big sample is representative. Asking "Do the sample's group proportions match the population's?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

150

Assuming a big sample is representative — proportions must match, not just counts.

151

Checking only one variable — a sample can match on age yet miss on income.

152

Confusing the method with the result — random sampling helps, but you still verify the proportions match.

153

The procedure for law of large numbers (intuition) is the easy part; the trap is using it to predict short runs. Asking "Is the average of many independent trials settling toward the true mean as n grows?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

154

Using it to predict short runs — convergence is a long-run effect; 10 flips can stray far from 50%.

155

Slipping into the gambler's fallacy — the average approaches μ, but no single outcome is 'due'.

156

Expecting the count, not the average, to balance — it's the proportion that converges, while raw counts can drift apart.

157
Risk
Stuck Point

The procedure for risk is the easy part; the trap is ranking by probability alone. Asking "Am I combining the probability of a loss with the size of that loss?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

158
Risk
Mistake

Ranking by probability alone — multiply by the loss amount so severity counts.

159
Risk
Mistake

Ranking by severity alone — a catastrophic but near-impossible event may carry little expected loss.

160
Risk
Mistake

Adding probability and loss instead of multiplying — Expected Loss is P×amount, a product.

161
Uncertainty
Stuck Point

The procedure for uncertainty is the easy part; the trap is forcing an exact answer onto an uncertain situation. Asking "Is precise prediction impossible because information is incomplete?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

162
Uncertainty
Mistake

Forcing an exact answer onto an uncertain situation — use a range or probability instead.

163
Uncertainty
Mistake

Confusing uncertainty with randomness — uncertainty can come from missing info, not just random outcomes.

164
Uncertainty
Mistake

Treating an estimate as a guarantee — an estimate still carries uncertainty and should be hedged.

165
Prediction
Stuck Point

The procedure for prediction is the easy part; the trap is reporting a prediction as an exact number with no range. Asking "Am I stating a value I have not observed, with a sense of how uncertain it is?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

166
Prediction
Mistake

Reporting a prediction as an exact number with no range - every prediction needs an uncertainty bound, not false precision.

167
Prediction
Mistake

Predicting far outside the data range and trusting it - patterns can break beyond where you have evidence.

168
Prediction
Mistake

Confusing a strong correlation with a guaranteed prediction - correlation tells you the relationship exists, not that the next case obeys it.

169

The procedure for model fit (intuition) is the easy part; the trap is judging fit only on the data used to build the model. Asking "Am I comparing a model's predicted values to the actual observed values to judge the gap?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

170

Judging fit only on the data used to build the model - good fit must hold up on data the model has not seen.

171

Treating a perfect fit as the goal - a model that matches every point exactly is usually memorizing noise.

172

Ignoring the direction and pattern of residuals - if residuals curve, the model has the wrong shape even if the gaps are small.

173

The procedure for overfitting (intuition) is the easy part; the trap is picking the model with the lowest training error. Asking "Does the model do much better on the data it was trained on than on fresh data?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

174

Picking the model with the lowest training error - overfit models always win on training; judge on held-out data.

175

Adding more parameters or wiggles to chase a better training score - extra complexity buys memorization, not generalization.

176

Calling any high-error model overfit - overfitting is specifically LOW training error with HIGH new-data error.

177

The procedure for underfitting (intuition) is the easy part; the trap is assuming poor accuracy always means overfitting. Asking "Does the model do badly even on the data it was trained on?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

178

Assuming poor accuracy always means overfitting - if training accuracy is also poor, it is underfitting.

179

Keeping a model simple to avoid overfitting and ignoring that it never fit at all - too simple is its own failure.

180

Blaming the data when the model can't even match training points - a too-simple model misses real structure that is genuinely there.

181
Data Visualization
Stuck Point

The procedure for data visualization is the easy part; the trap is using the wrong chart type for the data. Asking "Am I turning data into a picture so a pattern is easy to see?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

182

Using the wrong chart type for the data - bar graphs compare categories, line graphs show change over time.

183

Leaving off axis labels, titles, or a scale - an unlabeled graph can't be read correctly.

184

Assuming a fancier graph is a clearer graph - the best visualization is the one that makes the pattern obvious.

185
Misleading Graphs
Stuck Point

The procedure for misleading graphs is the easy part; the trap is trusting a graph because the data is real. Asking "Does the picture exaggerate or hide a difference that the actual numbers don't support?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

186

Trusting a graph because the data is real - the distortion lives in the design choices, not the numbers.

187

Only checking the bars and ignoring the axis - the truncated axis is the most common trick.

188

Assuming any surprising graph is misleading - confirm a specific distortion (axis, interval, scale) before crying foul.

189
Scale Distortion
Stuck Point

The procedure for scale distortion is the easy part; the trap is calling every nonzero axis a distortion. Asking "Is the axis baseline or interval spacing making a difference look bigger or smaller than it really is?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

190

Calling every nonzero axis a distortion - some quantities (temperature, year) legitimately don't start at zero; ask whether it misrepresents the difference.

191

Comparing bar heights without reading the axis numbers - the height is only meaningful relative to the baseline.

192

Ignoring uneven intervals on an axis - jumps from 0,10,20 then 20,50,100 distort the slope of the trend.

193
Aggregation
Stuck Point

The procedure for aggregation is the easy part; the trap is aggregating groups of different sizes by raw totals. Asking "Am I collapsing many individual values into a single summary number for the group?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

194
Aggregation
Mistake

Aggregating groups of different sizes by raw totals - compare proportions or rates when group sizes differ, not bare counts.

195
Aggregation
Mistake

Trusting one summary number to tell the whole story - an aggregate hides spread, outliers, and subgroups.

196
Aggregation
Mistake

Averaging numbers that are already averages without weighting - combine the underlying counts, not the summaries directly.

197

The procedure for normalization (statistics) is the easy part; the trap is comparing raw counts from groups of different sizes. Asking "Am I dividing by group size or rescaling so different-sized quantities can be compared fairly?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

198

Comparing raw counts from groups of different sizes - divide each by its group size to get a fair rate first.

199

Forgetting the multiplier when rates are tiny - 'per 100,000' keeps rare-event rates readable instead of like 0.00003.

200

Normalizing by the wrong base - match the denominator to the population actually at risk, not just any total.

201
Proportional Data
Stuck Point

The procedure for proportional data is the easy part; the trap is comparing raw counts across groups of different sizes. Asking "Am I expressing a count as a fraction of its own total so different-sized groups compare fairly?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

202

Comparing raw counts across groups of different sizes - convert each to a proportion of its own total first.

203

Reporting a count with no denominator - 'x out of n' is the whole point; the base gives the count meaning.

204

Mixing up part-to-whole with part-to-part - a proportion divides by the total, a ratio divides by the other part.

205

The procedure for comparative statistics is the easy part; the trap is comparing only the means and ignoring the spread. Asking "Am I weighing two or more groups against each other rather than describing a single group?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

206

Comparing only the means and ignoring the spread - two groups with equal averages can differ enormously in variability.

207

Declaring a difference real just because the numbers differ - a small gap may be noise, not signal.

208

Comparing groups of very different sizes by raw totals - use proportions or per-group rates to compare fairly.

209

The procedure for probabilistic thinking is the easy part; the trap is treating a high probability as a guarantee. Asking "Am I reasoning about an uncertain event in terms of likelihood and multiple outcomes, not a single certainty?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

210

Treating a high probability as a guarantee - 'likely' leaves real room for the other outcome.

211

Demanding a single yes/no answer when the situation is uncertain - reason in likelihoods and plan for more than one branch.

212

Ignoring low-probability, high-impact events - rare doesn't mean it can't matter when it hits.

213

The procedure for decision under uncertainty is the easy part; the trap is choosing the option with the largest possible payoff. Asking "Am I choosing an action by weighing each option's outcomes against their probabilities?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

214

Choosing the option with the largest possible payoff - weight it by probability; a big prize at low odds may have low expected value.

215

Ignoring risk and using expected value alone - two options with equal EV can differ hugely in how risky they are.

216

Letting one dramatic outcome dominate the choice - account for ALL outcomes and their chances, not just the memorable one.

217

The procedure for binomial coefficient is the easy part; the trap is using (nk) when order matters. Asking "Am I counting selections of k from n where order doesn't matter (or the matching expansion coefficient)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

218

Using (nk) when order matters - if arrangement counts, use a permutation, which is k! times bigger.

219

Computing all of n! instead of canceling - (nk)=n!k!(n−k)! cancels most factors; never multiply out giant factorials.

220

Forgetting (nk)=(nn−k) - choosing which k to keep equals choosing which n−k to leave; use the smaller k to compute.

221

The procedure for binomial distribution is the easy part; the trap is applying it when trials aren't independent or p changes. Asking "Are there a fixed number of independent trials, each success/failure with the same probability, and I want a count of successes?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

222

Applying it when trials aren't independent or p changes - drawing without replacement is hypergeometric, not binomial.

223

Dropping the (nk) factor - you must count the orderings of the k successes, not just multiply pk(1−p)n−k.

224

Mismatching the exponents - the success power is k and the failure power is n−k; swapping them inverts the answer.

225

The procedure for sampling distribution is the easy part; the trap is using the population SD σ as the spread of the mean. Asking "Am I describing how a statistic (like xˉ) varies across many samples, rather than how raw values vary?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

226

Using the population SD σ as the spread of the mean - the sample mean's spread is the smaller standard error σn.

227

Confusing the data's distribution with the statistic's distribution - raw values and sample means have different spreads.

228

Thinking a bigger sample makes individual data less variable - bigger n shrinks the spread of the MEAN, not of the data.

229

The procedure for central limit theorem is the easy part; the trap is claiming the raw data becomes normal. Asking "Am I claiming the distribution of a sample MEAN is approximately normal because the sample is large?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

230

Claiming the raw data becomes normal - the CLT is about the distribution of the MEAN, not the individual values.

231

Applying it with a tiny sample from a very skewed population - n≥30 is a rule of thumb; heavy skew needs even larger n.

232

Forgetting the spread shrinks - the sample mean's SD is σn, not σ.

233

The procedure for confidence interval is the easy part; the trap is saying '95% chance the true value is in THIS interval'. Asking "Am I building a range from a sample that likely contains the true population value at a stated confidence?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

234

Saying '95% chance the true value is in THIS interval' - the parameter is fixed; 95% refers to the procedure over many samples.

235

Using the data's SD as the spread of the estimate - the interval uses the standard error sn, not s alone.

236

Picking the wrong critical value - z∗=1.96 for 95%, not for 90% or 99%; match z∗ to the confidence level.

237
Margin of Error
Stuck Point

The procedure for margin of error is the easy part; the trap is reporting the full interval width as the margin of error. Asking "Am I reporting how far an estimate might be from the truth as a single ± value (half the interval width)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

238

Reporting the full interval width as the margin of error - the margin is HALF the width.

239

Using the data's SD instead of the standard error - the margin is z∗sn, which shrinks with bigger n.

240

Thinking margin of error covers bias or bad sampling - it only captures random sampling variability, not a flawed survey design.

241
Hypothesis Testing
Stuck Point

The procedure for hypothesis testing is the easy part; the trap is treating 'fail to reject H0' as 'prove H0 true'. Asking "Am I deciding whether sample data is surprising enough to reject a specific stated claim about a population?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

242

Treating 'fail to reject H0' as 'prove H0 true' - it only means insufficient evidence against it.

243

Choosing α after seeing the data - set the significance level before testing to avoid cherry-picking.

244

Confusing the null and alternative - H0 is the default 'no effect' claim; Ha is what you suspect.

245
P-Value
Stuck Point

The procedure for p-value is the easy part; the trap is reading the p-value as the probability the null hypothesis is true. Asking "Am I computing the probability of data this extreme assuming the null is true (not the probability the null is true)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

246
P-Value
Mistake

Reading the p-value as the probability the null hypothesis is true - it is the probability of the data given the null, not of the null given the data.

247
P-Value
Mistake

Concluding H0 is true when p is large - a large p-value means insufficient evidence to reject, never proof the null holds.

248
P-Value
Mistake

Comparing the p-value to the wrong tail or forgetting two-sided - use ∣Z∣≥∣zobs∣ for a two-sided test, doubling the one-tail area.

249

The procedure for type i and type ii errors is the easy part; the trap is swapping Type I and Type II. Asking "Am I classifying a wrong decision by comparing what the test concluded against what is actually true?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

250

Swapping Type I and Type II - Type I rejects a TRUE null (false alarm), Type II misses a FALSE null (missed detection).

251

Believing you can shrink both errors at once for fixed sample size - lowering α raises β; only more data shrinks both.

252

Calling a correct rejection an error - rejecting a false null is power (1−β), the desired outcome, not a mistake.

253

The procedure for experimental design is the easy part; the trap is skipping random assignment but still claiming causation. Asking "Does the researcher actively assign subjects to treatments (rather than just observe what they already do)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

254

Skipping random assignment but still claiming causation - only randomized assignment to treatments justifies a cause-and-effect conclusion.

255

Using one subject per treatment - replication (many subjects) is needed so one fluke result doesn't drive the conclusion.

256

Confusing the control group with 'do nothing' - the control gets a placebo or standard treatment so the only difference is the treatment itself.

257

The procedure for observational vs experimental studies is the easy part; the trap is claiming an observational study proved causation. Asking "Did the researcher assign the treatment to subjects, or only observe a group that already had it?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

258

Claiming an observational study proved causation - without random assignment, only association can be claimed.

259

Thinking 'large sample' upgrades an observational study to causal - size doesn't remove confounders; only random assignment does.

260

Calling any study with two groups an experiment - if subjects already belonged to their group, it's observational.

261
Sampling Methods
Stuck Point

The procedure for sampling methods is the easy part; the trap is equating a large sample with a representative one. Asking "Is the focus on the RULE for choosing who enters the sample (rather than how to assign treatments or compute a statistic)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

262

Equating a large sample with a representative one - a biased method (convenience) stays biased no matter how big it gets.

263

Mixing up stratified and cluster sampling - stratified takes some from every subgroup; cluster takes everyone from a few chosen subgroups.

264

Calling systematic sampling random - picking every 10th person is only unbiased if the list has no hidden periodic pattern.

265

The procedure for geometric distribution is the easy part; the trap is using the binomial because both involve p and 1−p. Asking "Am I counting the number of trials up to and including the first success (not the number of successes in a fixed set of trials)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

266

Using the binomial because both involve p and 1−p - the geometric has no fixed n; it counts trials until the first success.

267

Writing the exponent as k instead of k−1 - the first k−1 trials are failures, so it's (1−p)k−1⋅p.

268

Forgetting the trials must be independent with constant p - if p changes or trials are dependent, the geometric model fails.

269
Chi-Square Test
Stuck Point

The procedure for chi-square test is the easy part; the trap is dividing by Observed instead of Expected. Asking "Are the data counts of cases falling into categories, being compared to expected counts (rather than means or continuous values)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

270

Dividing by Observed instead of Expected - the formula is (O−E)2E, scaling each gap by the expected count.

271

Using percentages or means as the data - chi-square requires raw category counts, not proportions or averages.

272

Using the wrong degrees of freedom - goodness-of-fit uses df=k−1; a two-way independence test uses df=(r−1)(c−1).

273

The procedure for least squares regression line is the easy part; the trap is minimizing perpendicular or horizontal distances. Asking "Am I fitting a single straight line to two-variable numeric data by minimizing squared vertical distances?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

274

Minimizing perpendicular or horizontal distances - LSRL minimizes squared VERTICAL distances (y residuals) only.

275

Confusing the slope b with the correlation r - they relate by b=rsysx; b has units, r does not.

276

Extrapolating far outside the data's x-range - the line is only trustworthy across the observed x values.

277
Residuals
Stuck Point

The procedure for residuals is the easy part; the trap is computing predicted minus observed. Asking "Am I taking one point's actual value minus the line's predicted value to measure its individual miss?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

278
Residuals
Mistake

Computing predicted minus observed - the standard is observed minus predicted, y−y^.

279
Residuals
Mistake

Expecting nonzero residuals to sum to something meaningful - for an LSRL the residuals always sum to zero, so use squared residuals to measure total error.

280
Residuals
Mistake

Ignoring a curved pattern in the residual plot - a clear curve means a line is the wrong model, even if individual residuals are small.

281

The procedure for coefficient of determination is the easy part; the trap is reporting r when the question asks for r2. Asking "Am I reporting the fraction of y's variation explained by the linear model (a 0-to-1 number), not the slope or the correlation's sign?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

282

Reporting r when the question asks for r2 - square the correlation; r=0.7 gives r2=0.49, not 0.7.

283

Reading r2 as causation - it measures explained variation, never that x causes y.

284

Letting r2 go negative or above 1 - it's a proportion between 0 and 1, so any value outside that range is an error.

285

The procedure for inference for regression is the easy part; the trap is treating a nonzero sample slope as proof of a population relationship. Asking "Am I testing whether the underlying population slope is nonzero (rather than just computing or describing the sample slope)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

286

Treating a nonzero sample slope as proof of a population relationship - test b against its standard error before concluding β1≠0.

287

Using the wrong degrees of freedom - regression inference uses df=n−2, not n−1.

288

Forgetting the conditions (linearity, independence, equal spread, normal residuals) - the t-test is only valid when the regression assumptions hold.

289
Power of a Test
Stuck Point

The procedure for power of a test is the easy part; the trap is confusing power with α. Asking "Am I asking for the probability of correctly rejecting the null GIVEN it is false (the detection rate)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

290

Confusing power with α - power conditions on H0 being FALSE; α conditions on H0 being TRUE.

291

Thinking power and β add to nothing useful - power =1−β, so a Type II error rate of 0.2 means power 0.8.

292

Believing a non-significant result proves no effect - a low-power test often misses real effects, so 'not significant' isn't 'no effect.'

293
Paired t-Test
Stuck Point

The procedure for paired t-test is the easy part; the trap is treating paired data as two independent samples. Asking "Is every value in one group paired with exactly one specific value in the other (so I can form a difference per pair)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

294

Treating paired data as two independent samples - form the per-pair differences and run a one-sample test on them.

295

Using df=n1+n2−2 - the paired test uses df=n−1 where n is the number of PAIRS.

296

Using s of one group instead of sd - the test uses the standard deviation of the differences, not of either original column.

297
Two-Sample Tests
Stuck Point

The procedure for two-sample tests is the easy part; the trap is running a two-sample test on paired data. Asking "Are the two groups made of different, unrelated subjects with no natural pairing between them?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

298

Running a two-sample test on paired data - if subjects are matched, use the paired t-test on differences instead.

299

Using a single pooled standard deviation by default - the two-sample t-test typically uses s12/n1+s22/n2 with separate variances.

300

Choosing a t-test for proportion data - compare proportions with the two-proportion z-test, not the t-test for means.

301

The procedure for compound probability is the easy part; the trap is adding for 'and' or multiplying for 'or'. Asking "Does the problem combine two or more events with 'and' (multiply) or 'or' (add minus overlap)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

302

Adding for 'and' or multiplying for 'or' - 'and' multiplies; 'or' adds then subtracts the overlap.

303

Forgetting to subtract the overlap in an 'or' problem - use P(A)+P(B)−P(A and B) unless the events are mutually exclusive.

304

Using P(B) instead of P(B∣A) for dependent events - when the first event changes the second, multiply by the conditional probability.

305

The procedure for experimental vs. theoretical probability is the easy part; the trap is reporting 12 when the problem gives trial results. Asking "Does the probability come from reasoning about the possible outcomes (theoretical) or from counting what occurred in real trials (experimental)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

306

Reporting 12 when the problem gives trial results - if data is provided, use observed-over-trials, not the theoretical value.

307

Expecting experimental to equal theoretical in a few trials - they only converge over MANY trials (law of large numbers).

308

Thinking a deviation in 20 flips means the coin is unfair - small samples wander; only large, persistent deviations suggest bias.

309

The procedure for mean absolute deviation is the easy part; the trap is forgetting the absolute value. Asking "Am I averaging the ABSOLUTE distances of each value from the mean (not squared distances, not signed ones)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

310

Forgetting the absolute value - signed deviations from the mean sum to zero, so you must take ∣xi−xˉ∣ first.

311

Squaring the deviations - that gives variance/standard deviation; MAD uses absolute value, not squares.

312

Dividing by the wrong count - divide the total absolute deviation by n, the number of data values.

313
Two-Way Tables
Stuck Point

The procedure for two-way tables is the easy part; the trap is confusing joint, marginal, and conditional frequencies. Asking "Are two categorical variables being crossed in a grid so each cell counts a combination of one category from each?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

314

Confusing joint, marginal, and conditional frequencies - joint is one cell's count (divide by the grand total for a joint relative frequency), marginal is a row/column total, conditional is a cell over a row (or column) total.

315

Dividing a cell by the grand total when a conditional is asked - condition on the given group by dividing by that row or column total.

316

Putting a numeric variable in the table - two-way tables cross two CATEGORICAL variables, not measurements.

317
Bayes' Theorem
Stuck Point

The procedure for bayes' theorem is the easy part; the trap is treating P(H∣E) as equal to P(E∣H). Asking "Am I given P(E∣H) and a prior, and asked for the flipped P(H∣E)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

318

Treating P(H∣E) as equal to P(E∣H) - Bayes flips them, and the prior makes the two differ.

319

Ignoring the base rate (prior) - a rare condition keeps the posterior low even after strong evidence.

320

Using the wrong denominator - P(E) must total over ALL hypotheses (true and false), e.g. true positives plus false positives.

321
Line Plots
Stuck Point

The procedure for line plots is the easy part; the trap is leaving out values with zero marks. Asking "Am I stacking a mark for each data point above its value on a number line to show frequency?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

322
Line Plots
Mistake

Leaving out values with zero marks - keep every value on the number line evenly spaced, even if its stack is empty.

323
Line Plots
Mistake

Treating it like a category bar graph - line plots need evenly spaced NUMERIC values, not category labels.

324
Line Plots
Mistake

Miscounting frequency - the number of stacked marks above a value IS its frequency, so count carefully.

325

The procedure for population vs sample is the easy part; the trap is calling the data you collected 'the population' just because it is all the data you have. Asking "Is this number describing every single member I care about, or only the subset I actually collected data from?" first is what keeps a correct-looking calculation from being attached to the wrong concept.

326

Calling the data you collected 'the population' just because it is all the data you have - the population is the full group you want to conclude about, usually larger than what you measured.

327

Mixing up the symbols μ and xˉ - μ is the population mean (whole group) and xˉ is the sample mean (the subset).

328

Assuming any sample represents the population - only a sample chosen to reflect the whole group can stand in for it; a biased subset cannot.